Learning about the Enforcement of Conditional
Welfare Programs: Evidence from Brazil∗
Fernanda Brollo
Katja Maria Kaufmann
Eliana La Ferrara
This version: March 2017
Abstract
We study the implementation of Bolsa Familia, a program that conditions
cash transfers to poor families on children’s school attendance. Using unique
administrative data, we analyze how beneficiaries respond to the enforcement
of conditionality. Making use of random variation in the day on which punishments are received, we find that school attendance increases after families are
punished for past noncompliance. Families also respond to penalties experienced by peers: a child’s attendance increases if her own classmates, but also
her siblings’ classmates (in other grades or schools), experience enforcement.
As the severity of penalties increases with repeated noncompliance, households’ response is larger when peers receive a penalty that the family has not
(yet) received. We thus find evidence of spillover effects and learning about
enforcement.
∗
Fernanda Brollo, University of Warwick, CAGE and CEPR, [email protected]; Katja
Maria Kaufmann, Mannheim University, CESifo and IZA, [email protected];
Eliana La Ferrara, Bocconi University, IGIER and LEAP, [email protected]. We thank
Manuela Angelucci, Josh Angrist, Felipe Barrera-Osorio, Esther Duflo, Caroline Hoxby, Robert
Jensen, Leigh Linden, Marco Manacorda, Karthik Muralidharan, Johannes Rincke, Jeff Smith,
Michele Tertilt, Eric Weese, conference and seminar participants at Dartmouth, EUDN, Harvard,
Michigan, MIT, NBER, Namur, Paris School of Economics, Toulouse School of Economics, Uppsala, Universitat Pompeu Fabra and Yale for helpful comments. Giulia Zane, Simone Lenzu and
Emanuele Colonnelli provided excellent research assistance.
1
Introduction
Governments around the world increasingly rely on ‘conditional’ welfare programs
in many different areas, including unemployment and social assistance benefits,
maternity grants, child support and support for asylum seekers. Existing evaluations of conditional programs provide evidence on the combined effect of formal
rules and the enforcement of these rules, but not on the role of enforcement itself.
Yet understanding such role is indispensable for offering policy advice on program
implementation, given that monitoring and enforcement are costly. Furthermore,
political or administrative constraints may limit the extent to which governments
are able (or willing) to enforce conditionalities. This paper investigates how the
enforcement of program conditions affects beneficiaries’ behavior in the context of
conditional cash transfer (CCT) programs. CCT’s provide a stipend to poor families
as long as they meet certain conditions and have become a widely used tool to fight
poverty in low and middle-income countries.
We study the implementation of the “Bolsa Familia Program” (BFP) in Brazil,
a large-scale CCT that provides monthly subsidies to poor families conditional on
school attendance of all school-aged children being at least 85 percent of school
days every month. Failure to comply with this condition implies the receipt of
up to five warnings and penalties which increase in severity with the number of
past violations. The goal of our paper is to analyze whether people respond to the
enforcement of BFP conditions by adjusting school attendance and whether they
learn about the quality of enforcement from experiences of their peers.
From a theoretical point of view, it is not obvious that one should observe an
increase in school attendance in response to the receipt of a warning. First, the
family may not be able to (or want to) adjust on this margin, e.g., if the fall in
attendance was due to a particularly severe shock which persists. Second, even if
there is room for adjustment, the timing of it may not necessarily coincide with the
receipt of a warning. If families expect that the government will detect and punish
noncompliance with probability one, they should react already at the time when
they fail to meet the program conditions. If, on the other hand, families believed
that this probability were smaller than one, then they should respond after they
1
receive the warning. Apart from responding to their own warnings, families might
also respond to their peers’ experiences: learning that someone else was punished
for not attending school should lead to updating one’s beliefs about the strictness of
enforcement and to increasing school attendance in response.
To test these hypotheses we make use of a unique dataset that we compiled
from administrative sources. It covers the universe of BFP beneficiaries in the
Northeast of Brazil and includes information on child and family characteristics,
monthly records on school attendance of each child, warnings received and benefits
disbursed for the years 2008-2009. By merging these data with the Brazilian school
census, we are also able to identify children of other BFP beneficiaries who are
in the same class, grade or school as the family’s own children. This allows us to
construct different sets of peers.
We present our results in two parts. In both, our outcome of interest is the
likelihood that individuals fail to comply with the school attendance condition in a
given month (in short, “noncompliance”). In the first part we analyze the extent to
which people respond to their own experiences of enforcement. We find that the
likelihood of noncompliance decreases after receiving a warning or penalty. The
estimated size of the effect is a decrease of 4 percentage points, which represents a
30 percent decrease over the average monthly noncompliance rate.
To provide evidence that we identify a causal effect we exploit random variation in the timing of arrival of warnings within each month. The date at which
households can withdraw their monthly transfers –and receive the warning message, if applicable– depends on the last digit of the head’s social security number,
which is random. We can thus compare households who receive warnings earlier
in the month with households who receive them later: the former should display
a stronger contemporaneous reaction because they have more time to adjust their
children’s school attendance in that month, which is what we find.
In the second and main part of the paper we study whether beneficiaries react to
warnings received by other households. The goal is to shed light on the importance
of information transmission and learning in the context of program enforcement
and to quantify potential spillovers that matter for estimating the benefits of stricter
enforcement. We start by estimating if the likelihood that a child does not com2
ply responds to the share of “peers” who received warnings in that month or in the
month before, controlling for the household’s own warnings. We use different definitions of peers, including BFP beneficiaries who are (i) a child’s own classmates;
(ii) classmates of the child’s siblings (typically of different age); and (iii) classmates
of the child’s siblings who attend a different school. In all cases we find that warnings received by peers induce a decrease in noncompliance in the order of 1.1 (2.3)
percentage points in the same (subsequent) month when all of one’s peers receive
a warning. This effect does not seem to be driven by correlated shocks: effects
are very similar whether we focus on a child’s own classmates (who are likely to
experience similar shocks) or on the classmates of a child’s sibling who attends a
different school. Also, as a falsification test we show that there is no evidence of an
anticipated response.
To investigate the learning process more in depth, we make use of the fact that
families progress through different “warning stages” and receive increasingly severe
penalties if they repeatedly fail to comply. When we distinguish between peers
who get penalized at a lower warning stage than the family’s own, and peers who
receive warnings for higher stages, the latter induce a larger decrease in individual
noncompliance. This is consistent with our learning interpretation because those
warnings convey new information on the likelihood that the government implements
higher order punishments.
Finally, to further corroborate our learning interpretation, we analyze a different
set of peers, that is, BFP beneficiaries who live in the same zip code as the family.
People living in the same area are likely to pick up the transfer from the same local
service point, so we exploit the quasi-random variation in the day of the month on
which beneficiaries can withdraw the money to construct an exogenous set of peers
with whom recipients may interact. We then test whether warnings to beneficiaries who live in the same zip code and can cash in the benefit on the same day as
family i affect the likelihood of noncompliance of i’s children, after controlling for
warnings to BFP families in i’s zip code.1 We find significant effects in the same
and in the following month, consistent with the existence of information spillovers
among families living in the same area. Also in this case, warnings received by
1
The latter is included to control for possible geographically correlated shocks.
3
others for higher stages than one’s own have stronger effects. The fact that we find
evidence of information transmission using two sets of peers that are based on two
entirely different identification strategies increases our confidence in the validity of
our results.
Our paper contributes to several strands of literature. First, there is a relatively
small literature on estimating behavioral responses to imperfect program enforcement. Banerjee, Glennerster and Duflo (2008) discuss the implications of imperfect
enforcement in the Indian health sector; Rincke and Traxler (2011) and Drago,
Mengel and Traxler (2015) analyze spillovers from enforcement of compliance
with TV license fees; Lochner (2007) investigates the effect of learning about arrest probabilities on criminal behavior. Earlier work by Black, Smith, Berger and
Noel (2003), Van den Berg, van der Klaauw and van Ours (2004) and Lalive, van
Ours and Zweimüller (2005) studies the effects of unemployment insurance programs that monitored job search effort. Aside from the difference in context, our
paper contributes to the above literature by focusing on the process through which
beneficiaries learn about the quality of enforcement, such as the importance of information transmission through different types of signals and via different types of
peers.2
Our paper is also related to a large literature on CCT’s. Among others, Schultz
(2004), Todd and Wolpin (2006) and Attanasio, Meghir and Santiago (2012) estimate the impact of Progresa/Oportunidades in Mexico; Bourguignon, Ferreira
and Leite (2003), De Janvry, Finan and Sadoulet (2011) and Bursztyn and Coffman (2012) study Bolsa Escola, the predecessor of Bolsa Familia in Brazil, while
Bastagli (2008), De Brauw et al (2015a,b) and Chioda, de Mello and Soarez (2016)
focus on Bolsa Familia. In contrast to the above literature, we focus on the enforcement aspect of CCT’s. There are a few papers which analyze the enforcement of
eligibility criteria, i.e. errors of type one and two in terms of families included in or
excluded from the program (e.g., Cameron and Shah, 2014), but there is very little
evidence on the enforcement aspect of conditionalities. One notable exception is
DeBrauw and Hoddinott (2010) who test the direct effect of program conditions in
2
Also, since we do not have direct measures of beliefs about enforcement, we infer them from
individuals’ behavior, akin to the approach in Chetty, Friedman and Saez (2013).
4
the context of Progresa by exploiting the fact that some beneficiaries who received
transfers did not receive the forms needed to monitor school attendance. They use
matching and fixed effect methods to show that the absence of these forms significantly reduced compliance.
Within the CCT literature Schady and Araujo (2006), Baird, McIntosh and
Özler (2011) and Benhassine et al. (2015) compare the effectiveness of conditional
versus unconditional cash transfers (UCT). The first two papers find that conditionality (or the belief of it) improves school attendance, while the latter paper concludes that an unconditional transfer which is “labeled” as education support is
equally effective. Our contribution differs from the CCT versus UCT comparison.
In a world where conditionality nominally exists but program recipients anticipate
that it will not be enforced, one may fail to find a difference in the impact of the two
types of programs.3 But this does not imply that conditionality, if enforced, would
be uneffective. Our paper is precisely an attempt to understand how people update
their beliefs about enforcement after experiencing it (directly or through peers) and
change their behavior in response.
Finally, several papers analyze peer effects and spillovers in the context of conditional cash transfer programs, e.g., Barrera-Osorio, Bertrand, Linden and PerezCalle (2011) for Colombia; Angelucci et al (2010), Angelucci and De Giorgi (2009)
and Bobonis and Finan (2009) for the Mexican program Progresa/Oportunidades.
Compared to this literature, our focus is not to identify conventional or “direct”
peer effects (such as the effect of peers’ school attendance on own attendance), but
on the effect of peer warnings (a signal about the quality of enforcement) on individual attendance. This has the advantage of mitigating some of the identification
problems that the conventional peer effect literature has to face.4
The remainder of the paper is organized as follows. In section 2 we provide
background information on Bolsa Familia, while in section 3 we present the data
and descriptive statistics. In sections 4 and 5 we discuss our empirical strategy and
3
For example, Schady and Araujo (2006) conclude that cash transfers can be effective without
monitoring but hypothesize that the effect of unenforced conditions might dissipate once households
realize that they will not be punished.
4
Our interest in how people learn about program features from their peers is shared, for example,
by Duflo and Saez (2003).
5
results on whether individuals respond to experiencing enforcement and whether
they learn from peers, respectively. Section 6 concludes.
2
Background Information on Bolsa Familia
The Bolsa Familia Program (BFP) reaches around 14 million Brazilian families,
that is 60 million poor people (equivalent to about 30 percent of the Brazilian population) with an annual budget of over 24 billion reais (USD 11 billion, about 0.5
percent of GDP). Thus BFP reaches nearly three times as many people and is about
three times as large in terms of budget as the well-known conditional cash transfer
program Progresa/Oportunidades.
BFP was launched by the Brazilian president Inácio Lula da Silva in 2003 to
consolidate four different programs (Federal Bolsa Escola Program, Auxilio Gas,
Bolsa Alimentação, Fome Zero) into a single program.5 The implementation of the
program has seen a gradual evolution over the years. The election-free year 2005
was used to strengthen the core architecture of the program and to improve the registry of families. In 2006, the Ministry of Social Development (MDS) embarked
on initiatives to promote further vertical integration with sub-national CCTs and integrated the conditional transfers paid under the Child Labor Eradication Program
(PETI). The agenda for 2007 and beyond was to reinforce the monitoring and verification of conditionalities, to strengthen oversight and control mechanisms and
to continue improving the program’s targeting system. Notably, monitoring and
enforcement of conditionalities had been relatively weak in the first years of the
program, and were strengthened after 2006.
The targeting of the program was conducted in two steps. First, there was geographic targeting at the municipal level: the federal government allocated BFP
quotas to municipalities according to estimates of poverty. Within municipalities,
spatial maps of poverty were used to identify and target geographic concentrations
of the poor. The second step was to determine eligibility at the household level.
Eligibility was determined centrally by MDS based on household registry data that
was collected locally and transmitted into a central database known as the Cadastro
5
For a detailed description of the features of BFP, see Lindert et al. (2007).
6
Unico.
Benefits. BFP provides two types of benefits, a “base” and a “variable” transfer that depend on family composition and income. Families with a monthly per
capita family income of up to R$60 (US$30) are classified as “extremely poor”,
while families with between R$60 and R$120 are classified as “moderately poor”.
The base benefit is provided only to families in extreme poverty, regardless of their
demographic composition. Both extremely poor and moderately poor families receive a “variable” benefit which depends on the number of children in the family
(capped at three to avoid promoting fertility) and on whether the mother is pregnant
or breast-feeding. Benefit amounts are as follows. The base benefit amounts to R$
60 (approximately US$ 30, which is also the per capita income threshold for the
extremely poor), and the variable benefit to R$ 20. Benefit amounts and eligibility
thresholds are periodically adjusted for inflation.
To illustrate the magnitude of the program transfers, think of a family with
three children that is right at the threshold to be classified as extremely poor, i.e.,
they have a monthly per capita income of R$60 and a family income of R$ 300.
This family would receive monthly transfers of around R$120, which amounts to
40 percent of their total family income.
Conditionality. BFP cash transfers are conditional on all age-relevant family
members complying with requirements in terms of school attendance. Each schoolaged child between 6 and 15 has to attend at least 85 percent of school days each
month (absence due to health reasons is justified and does not count towards the
number of days absent). If a single child fails to meet this requirement in a given
month, the family is affected for the whole amount of the transfer, i.e. also for
quotas that pertain to other children. This element of “joint responsibility” for
children in the same family is a unique feature of BFP, e.g., compared to other
well-known CCTs such as Progresa/Oportunidades.6
BFP also has conditions related to health behavior, such as health check-ups
for pregnant women and vaccinations for children below age 5. Based on our data,
6
In 2008 a new subprogram, Benefı́cio Variável Jovem (BVJ), was added to BFP to increase
school attendance of teenagers aged 16 and 17. BVJ has its own set of conditions and warning
system and does not affect the family’s warning stage in the main program (i.e. for the children aged
6 to 15). We only have data for a few months on BVJ, hence we focus on children aged 6 to 15.
7
those conditions are rarely enforced and we do not observe individual responses to
enforcement of those conditions (in contrast to having monthly data on children’s
school attendance). Therefore we focus on children aged 6 to 15 and analyze responses to enforcement of school attendance conditions.
Penalties. The consequences of noncompliance vary depending on the historical record of compliance of each family. In the first case of noncompliance the
family receives a warning without any financial repercussion. With the second instance of noncompliance, the family receives a second warning and benefits are
blocked for 30 days, after which the family receives the accumulated benefit of the
previous and the current month. The third and fourth warnings lead to a loss of
benefits for 60 days each time and these benefits are never recovered. Finally, after
the fifth warning the benefit is canceled and the family loses eligibility. According
to the general rules, the family can re-apply to the program 18 months later. The 18
months rule is also used to “reset” a family warning history, e.g., if a family is in
warning stage 2 but then complies with the rules for 18 consecutive months, their
warning history goes back to stage zero.
Timing of penalties. Each month families can withdraw their transfer money
at a local service point with a Bolsa Familia “electronic benefit card”.7 In case
of noncompliance, at the time of withdrawal the family receives a warning message which specifies the penalty that the family incurs. To avoid bottlenecks at
the local service point, when families pick up their BFP transfers, each family is
assigned a pre-specified date each month starting from which the family can withdraw the transfer money (and contextually receive the warning). The exact date
in each month is determined by the last digit of the social security number of the
legally responsible adult of the family, which is basically random, as we will show.
In particular, the ten digits (0,1,...,9) correspond to the ten weekdays in the last two
weeks of the month.8 We will exploit this randomness to identify the causal impact
7
Local service points are either Caixa branches or Caixa “correspondents”. Caixa Econômica
Federal, a savings and credit union, is the government agency responsible for transferring BFP
benefits to the beneficiary families. Caixa has a large network of banking correspondents, which
are commercial establishments with a different business focus, used to expand access to remote and
particularly poor areas (Kumar et al., 2006).
8
Every family receives a benefit calendar with the information on when they can pick up the
8
of warnings received by a family on school attendance of its children.
Quality of information about the BFP program.
Families are well informed about transfer amounts, conditionalities and penalties:
these aspects are widely and regularly publicized on TV, radio and newspapers in
Brazil, and are spelled out in a booklet issued to each beneficiary family (Agenda de
Compromissos). In case of noncompliance, at the time of withdrawal of the transfer
money, the family receives a message that reports the family’s warning stage, the
month of noncompliance to which the warning refers, the names of the child(ren)
who failed and which type of warning they might receive in the next instances of
noncompliance.
An example of a warning message for a family receiving their first warning is:
“The family has not complied with the conditionalities of Bolsa Familia for the first
time. At this moment the payment will not be blocked. But if you fail to comply
again your benefit payment may be blocked, suspended or even cancelled.”9 Note
that the text does not say that the payment will be suspended with probability one,
hence there is a degree of uncertainty about the actual enforcement of conditionality
which is embedded in the system. This uncertainty is further reinforced by the
experience of lax enforcement in the early years of the program.
The implementation of this conditionality scheme involves different actors. First
of all, children’s attendance is recorded by school teachers. The school sends the attendance lists of students to the municipality, reporting the exact fraction of school
days attended in case attendance was below 85 percent, otherwise only reporting
that the student complied. Each municipality collects the lists and sends them to
the Ministry of Education (MEC), which determines whether the family as a whole
complied or not in a given month, i.e. whether all children between 6 and 15 attended at least 85 percent of school days. MEC sends a detailed report to the Ministry of Social Development (MDS), which establishes which warning the family
should receive in case of noncompliance and whether the family is entitled to the
transfer in the different months.
9
In addition to this short paragraph, the warning message repeats the general rules of BFP in a
clear and salient manner. It briefly mentions again the program conditions (i.e. of at least 85% of
school attendance of all school aged children) and which instance of noncompliance may lead to
which type of penalty.
9
transfer for that month (based on the warning stage reached).
The MDS sends this information to the Caixa Econômica Federal, a savings and
credit union that transfers the benefit amount to the bank account of the family if
the family is entitled to receiving the transfer for that month.
[Insert Figure 1]
These different steps of the process involve time and lead to a delay in terms
of the month in which the warning is received compared to the month of noncompliance. Figure 1 illustrates an example where the family failed to comply in the
month of February, right after the beginning of the school year, and received a
warning in May. We denote the difference between the month of warning and the
month of noncompliance as “delay”. There is substantial variation in the extent of
delay, which we make use of in our graphical motivation for analyzing the effect of
warnings on families’ behavior and in some robustnes checks which we conduct to
support our main findings. During our sample period this variable ranges from 2
to 6, with a mean of 3.8 months and a median of 3 months. Appendix Figure A.1
shows the frequency of different delays. As we will show, the variation in delay is
orthogonal to household and child characteristics and is entirely driven by time and
area effects.
3
Data
We make use of a unique dataset that we assembled combining several sources of
administrative data. The first source is the household registry (Cadastro Unico) held
by the Brazilian Ministry of Social Development (MDS), which contains socioeconomic characteristics of all BFP beneficiary households.10 We also know the
eight digit zip code (Código de Endereçamento Postal - CEP) of the neighborhood
where the household lives, which we will exploit in our analysis of learning. We
have information on the universe of households enrolled in the program during
10
For each household member the Cadastro Unico comprises information on age, gender, race,
marital status, education and employment status and for the household as a whole it reports expenditures, house property, garbage collection, connection to running water, electricity etc.
10
2008-2009 in the Northeast of Brazil, one of the poorest and largest regions in the
country, comprising 30 percent of the Brazilian population, and with more than
half of its inhabitants living in poverty. To conduct our analysis we extracted a 10
percent random sample, yielding a total of 478,511 households in the program.11
A second dataset from MDS contains monthly records of school attendance during 2008-09 for each child monitored for the attendance conditionality, i.e., each
child aged 6 to 15. We know whether the child complied with the attendance condition in a given month, and in case of noncompliance we know the exact fraction
of days attended below the threshold of 85 percent. This dataset also includes two
categories that qualify the absence: one is justifiable absences such as sickness, for
which the household does not incur any penalty; the other category is for unjustifiable absences (e.g., child labor, teen pregnancy, etc.) which instead count towards
the warnings.
A third dataset from MDS contains monthly information on warnings, which
allows us to create the complete warning history of each family. In particular, we
know in which month they received a warning, the month in which attendance failed
to meet the threshold and that gave rise to that particular warning, and the warning
stage in which the family is at any given point in time.
The fourth administrative dataset we use is payroll data, which contains monthly
information on the benefits that the family received and whether the benefit was
blocked or suspended in a given month. All four of these datasets can be linked
through the social security number (Número de Identificação Social - NIS) of the
household member legally responsible for the child or of the child him/herself.
We complement the above administrative records on BFP with two datasets
on schools. The first is the School Census compiled by the Ministry of Education,
which contains information on all children who are enrolled in a given school, grade
and class. We merge the School Census with the BFP administrative data using the
NIS code of the child when available in the School Census and otherwise based on
11
To improve our precision in estimating the effects of different warning stages, we over-sampled
households that were warned at least once during our sample period, and use regression weights
to correct for this. Since we include household or individual fixed effects in all our regressions,
households that are never warned do not contribute to estimating the effect of the main variable of
interest, namely the receipt of a warning.
11
area code, school code, grade, full name and date of birth of the child.12 This allows
us to identify the peers who are in the same school, grade and class for each child
and who are also recipients of BFP. This is important for our analysis to identify the
role of learning from classmates.
The final dataset we employ is Prova Brasil, collected by the Instituto Nacional
de Estudos e Pesquisas Educacionais Anı́sio Teixeira (INEP) to evaluate the quality
of education across Brazilian schools. These data include a questionnaire administered to principals of schools, containing, among other things, information on
the policies that the school adopts to inform parents about children’s unexcused absences. We exploit this information in one of the robustness checks for our analysis.
[Insert Table 1]
Table 1 presents summary statistics of the main variables of interest. A full
set of summary statistics for all variables is provided in Appendix Table A.1. The
outcome variable we use in our analysis is whether a family fails to comply with
BFP rules, i.e., at least one child attends less than 85 percent of school days in a
given month. We refer to this variable as “noncompliance”.
Panel A of Table 1 shows that on average the likelihood of noncompliance for
the household is 8.6 percent in any given month, and the likelihood of receiving a
warning is 3.5 percent. In the average month 29 percent of our households are in
warning stage 1, which means they have received a message about noncompliance
but not lost money; 8.5 percent are in warning stage 2, where the money is blocked
and then returned; 3 and 1 percent are in warning stages 3 and 4, respectively, where
the transfer is lost for two months, and 0.2 percent reach warning stage 5, when they
are expelled from the program.
Panel B of Table 1 shows that the average child who is a BFP recipient in our
sample has 16 other BFP recipients in her class, 52 in the same grade and 279 in the
same school. About 1 percent of one’s classmates who are BFP recipients (‘Peers’)
fail to meet the attendance conditionality in the average month, and 1.4 percent
receive a warning message (for any of the five warning stages).13
12
13
We are able to match 68% of individuals, 41% based on their NIS.
Since warnings are received at the household level, while the fraction of peers not complying
12
4
Own Experience of Enforcement
Before analyzing whether individuals learn about enforcement from peers, we investigate how individuals respond to experiencing enforcement themselves. In particular, we test whether households react to a warning by increasing the school
attendance of their children. We conduct this analysis at the household level because warnings are applied to the entire family and not to individual children. In
Appendix Table A.2 we show that results are very similar if we use the child as the
unit of observation.
From a theoretical point of view, it is not obvious that one should observe an
increase in school attendance in response to the receipt of a warning. The first
reason is that the family may not be able to (or not want to) adjust on this margin,
e.g., if the fall in attendance was due to a particularly severe and persistent shock.
The second reason has to do with the priors held by the household and its updating process. When deciding whether to fulfill program conditions, families compare
the costs and benefits of compliance. An essential part of this calculation is the belief they hold about the probability that the government will detect noncompliance
and punish them for it. If the family believed this probability to be one, then it
should already anticipate the consequences of noncompliance at the time when the
child fails to attend school, and should respond accordingly. The increase in attendance –if any– would not necessarily coincide with the receipt of a warning several
months later, but plausibly come earlier. If, on the other hand, the household believed that the probability of punishment were smaller than one, then on top of any
earlier response it should adjust its behavior upon receipt of a warning, in order to
avoid further penalties.
Identifying the causal effect of warnings on school attendance is empirically
challenging because the receipt of a warning is a function of past school attendance.
We therefore resort to a number of alternative strategies to establish a causal link
between receipt of a warning and attendance response.
are calculated at the individual child level, the fraction of peers in noncompliance is lower than the
fraction of peers warned, since not all children in a household fail to comply at the same time.
13
4.1
Graphical analysis
We start by visually exploring the pattern of noncompliance in the months before
and after the warning.
[Insert Figures 2 and 3]
Figure 2 pools data from the different types of warnings received by different
households and plots the probability that at least one child in the household fails to
meet the 85 percent attendance threshold against the number of months since the
warning was received. The value 0 on the horizontal axis indicates the month of
the warning, −1 is the month before, and 1, 2, ...5 indicate the number of months
after the warning was received. As can be seen from the figure, there is a clear discrete downward jump in noncompliance immediately after the receipt of a warning:
households respond by increasing attendance of their children, hence the likelihood
of noncompliance goes down. The probability of noncompliance remains relatively
constant in the months after the warning.
Appendix figure A.2 presents the same data disaggregated by warning stage,
i.e. separately for households that received their first warning (Warning Stage 1),
their second warning (Warning Stage 2), etc. until the fifth and last warning. The
pattern displayed in figure 2 is found across all warning stages except for the last
one, where the decrease in noncompliance is less discontinuous (note, however, that
very few people reach Warning Stage 5).
In figure 3 we repeat the exercise conditioning on the time elapsed between
noncompliance and the receipt of the warning, i.e. on “delay”. In this figure, we
indicate with 0 the month when the family failed to comply with the attendance
requirement and with a vertical line the month in which the warning is received.
Moving from left to right and from top to bottom, figure 3 shows what happens
to rates of noncompliance when the delay is 2, 3, ... up to 6 months.14 In t = 0
the probability of noncompliance is one by construction; from t = 1 onwards this
probability decreases to a ‘normal’ level, but once the warning is received, it jumps
down and stays at this lower level given the new (higher) warning stage.
14
See Appendix Figure A.1 for the frequency of different delays.
14
In all cases except for the delay of 6 months, we see a discrete jump in the
rate of noncompliance immediately after the receipt of a warning: if the delay is 2
months, then immediately after the arrival of the warning in month 2 the likelihood
of noncompliance jumps down; if the delay is 3 months, it jumps down in month
3, etc. This is important because it suggests that the adjustment was caused by the
receipt of the warning. Other possible reasons (e.g., mean reversion of the shock)
would generate a pattern where the adjustment would depend on the distance from
the month of noncompliance (month 0) and not necessarily correspond to the month
of the warning, i.e., the (shifting) vertical line. In other words, there is no reason
why mean reversion should cause a discrete jump downwards which happens with
the exact same delay as the warning.15 Also, the fact that we see a response of the
household upon arrival of the warning (i.e. a further reduction in the likelihood of
noncompliance) suggests that the warning was not fully anticipated.
4.2
Multivariate analysis
We next estimate the effects of warnings on noncompliance using multivariate regressions. As a first step, we want to regress noncompliance on the warning stage
that a household is in, since the warning stage determines the cost of not complying
with conditionality. One challenge in identifying this effect is that some households
have a much higher propensity to miss attendance than others, and these are the
households who reach higher warning stages. If we simply used cross-sectional
variation in the data, this would bias the (negative) coefficient on warnings towards
zero or even induce a positive correlation between receiving warnings and failure to
comply. We therefore use household fixed effects throughout our analysis to control
for time-invariant differences in the propensity to attend school. This implies that
we exploit variation within family over time in the warning stage reached, i.e. in
the receipt of new warnings.
15
Moreover, as we show in the next section, delay is orthogonal to household and child characteristics (see Appendix Table A.3).
15
Our baseline specification for estimating the effects of own warnings is:
Yht =
5
X
k
αk WS ht
+ γXht + Dt + Dh + ht
(1)
k=1
where h denotes the household, t the month, Y is a dummy equal to 1 when at
least one child in the household attends less than 85 percent of the school days in
a month (“noncompliance”); WS k denotes a dummy equal to one if the household
is in warning stage k (with k = 1, ..., 5); X is a vector of household level controls
including fraction of male children in the household, number of boys and girls in
different age brackets (6-10, 11-15, 16-18); Dt denotes month and year dummies to
control for seasonality and time effects; Dh denotes household fixed effects and is
the error term. Given the panel nature of our data, we estimate equation (1) and all
other regressions in this section using a linear probability model and clustering the
standard errors at the household level.
[Insert Table 2]
Table 2 shows our results. The probability of noncompliance decreases after the
household receives a warning and advances to a higher warning stage, confirming
the findings of our graphical analysis. The negative coefficients are of increasing
magnitude the higher the warning stage, but one should be careful when comparing
the effects of different warning stages because those coefficients are estimated by
averaging over different subsets of families. For example, the coefficient on warning stage 5 is only estimated for those families who ever get to warning stage 5
in our two-year period of observation, while the coefficient on warning stage 1 is
estimated over the set of families who receive at least the first warning during our
sample period. These households are likely to differ in unobservable ways, hence
we cannot attribute differences in the magnitude of the coefficients solely to the
incentive effects of larger penalties. Since our focus here is on whether and how
people respond to and learn about enforcement and not on the effects of different
warning stages, we leave a more detailed analysis of this issue for future analysis.16
16
To explore the effect of larger penalties, in Appendix Table A.4 we estimate the same regression
16
Appendix Table A.2 shows that the results are qualitatively similar if we conduct
the analysis at the individual (child) level, including child level fixed effects and
time varying controls.17
Causality
To show that we identify a causal effect of warnings on attendance behavior, we
exploit random variation in the timing of warning arrival. In particular, we make
use of the fact that the exact day of the receipt of warnings depends on the last
digit of the social security number of the legally responsible adult in the family, as
described in section 2. We conjecture that families who receive warnings earlier
should have more time to react to the new information, hence we expect a larger
behavioral response for these families compared to those who receive the warning
later in the month. In the limit, someone who receives a warning the last day of
the month could only adjust if her child’s attendance was just one day below the
threshold. To test this conjecture, we split the sample into “early” and “late” warning receivers, where “early” are the households that fall in the first half of the period
during which money can be withdrawn within a month and “late” are those that fall
in the second half. Appendix Table A.5 shows that observable characteristics are
almost perfectly balanced across the two groups (in the few cases where there are
significant differences, these are extremely small, at the third decimal digit). We
estimate the following modified version of Equation (1):
Yht =
5
X
k=1
αkE WS htE,k +
5
X
k=1
αkL WS htL,k +
5
X
E,k
βkE WS h,t−1
+
k=1
5
X
L,k
βkL WS h,t−1
+γXht +Dt +Dh + ht
k=1
(2)
holding the set of households constant by conditioning on the initial and last warning stage that the
households reach during our sample period. For example, for households that reach warning stage
3, we can compare the magnitude of the effects of warning stages 1 and 2 (the effect of warning
stage 3 cannot be interpreted for this subset of households, since by construction warning stage 3 is
the highest warning stage they will reach, which means that their noncompliance rate mechanically
decreases thereafter). Appendix Table A.4 shows that higher warning stages have stronger effects in
terms of reducing noncompliance for all subgroups.
17
The magnitude of the coefficients is smaller when estimated with individual level data because
not all children in a given household fail to comply at the same time.
17
where the superscripts E and L stand for “early” and “late”, respectively. The variable WS htE,k (WS htL,k ) is the interaction between the warning stage and a dummy taking value one if household h is an “early” (“late”) warning receiver. We also include
first lags of these variables to estimate delayed household responses. Our prior is
that αkE > αkL because during the month when the warning is received households
who are warned earlier have more time to adjust the attendance of their children.
On the other hand, since “early” and “late” households on average fail to comply at
the same rate, we expect “late” households to catch up during the following month,
hence we expect βkE < βkL .
[Insert Table 3]
E
Table 3 reports our estimates.18 Coefficients b
αkE , b
βk for “early” households are
L
displayed in column 1; coefficients b
αkL , b
βk for “late” ones in column 2, while they
are both estimated in the same equation. Column 3 reports the differences b
αkE −
E
L
b
αkL and b
βk − b
βk , with p-values in square brackets. The pattern of the estimated
coefficients is clear: households that receive warnings early respond more strongly
in the month of warning receipt, while households that receive warnings late catch
up in the following month and respond more strongly then. Given the randomness
of the “early” vs. “late” classification, it is difficult to rationalize this pattern with
explanations other than the fact that the household is responding to the actual receipt
of the warning and to its informational content.
To provide further support for this interpretation we show in Online Appendix
A that the same conclusion holds when using variation in the arrival of warnings
across months. In particular, we make use of the fact that the delay of warnings
varies over time in a non-monotonic way due to bureaucratic complexities and is
orthogonal to household characteristics.19 In Appendix Table A.6 we thus conduct
a difference-in-difference analysis comparing households who received warnings
18
The smaller number of observations in Table 3 compared to Table 2 is due to the fact that, by
introducing a lag in warning stage, we lose the first month of our sample period.
19
In Appendix Table A.3 we regress delay on household and child level controls, month and year
dummies and municipality dummies. We find that time and area fixed effects explain more than
98 percent of the variation and only one out of 23 household and child controls is significant at
the 10 percent level. The p-value for the joint test that the coefficients on all household and child
characteristics are zero is 0.91.
18
with different lags and show that there is a significant decrease in the probability
of noncompliance precisely after the receipt of the warning, in that the receipt of
a warning decreases noncompliance by 3.8 percentage points (equivalent to a 30
percent decrease).
4.2.1
Interpretation
A possible interpretation of our results so far is that when households receive a
warning, they learn not so much that the program is being enforced, but that their
children have missed school – something they may not have been aware of. While
this is certainly not a concern in our main analysis about learning from peers’ warnings (as discussed in the next section), we test the importance of this concern in
Appendix Table A.7 by exploiting variation in school policies regarding communications with families. Specifically, we merge our administrative data with a dataset
on schools called PROVA Brasil. PROVA contains some school-level variables that
capture whether parents receive information about non-attendance of their children
from the school, independently of BFP warnings. We compare schools that inform parents with schools that do not. Under the hypothesis that warnings have
an effect because parents learn about non-attendance of their children, the effect of
warnings should be smaller in schools where parents are already informed about
non-attendance. The results show, however, that there is basically no difference in
the effect of warnings between schools which inform parents and schools that do
not. This suggests that families’ response to warnings is unlikely to be entirely due
to learning about children’s non-attendance.20
Behavioral response vs teachers’ reporting One remaining interpretation issue
is the extent to which the behavioral responses we identify correspond to actual
20
Bursztyn and Coffman (2012) present evidence that the conditionality embedded in Brazil’s
CCT is a valuable source of information for parents and empowers them in the negotiation with
their children. The effect of warnings that we estimate could then be interpreted as resulting from
the improved ability of parents to commit to punishing their children when the parents themselves
are penalized by the government. While this interpretation would not be inconsistent with the results
in Appendix Table A.7, it cannot explain the learning from peers results that we present in the next
section.
19
increases in attendance, and not simply to more lenient reporting by teachers, e.g.,
because parents convince teachers to be less strict in registering non-attendance after they receive a warning.21 A first reaction to this is that even in this case our
hypothesis that families learn about the strictness of enforcement would be valid: it
would be the action taken by the family that would differ (e.g., persuading teachers
instead of sending children to school). Secondly, our results on warnings received
by peers –as discussed in the next section– help address this point to some extent.
In particular, we find that child i’s noncompliance goes down when the classmates
of i’s siblings get warned or when i’s neighbors receive warnings. Since the teacher
of child i would not know about those children’s warnings (in particular if the siblings and neighbors’ children attend different schools, for example because they are
of a different age), this result is more likely explained in terms of actual child’s
attendance as opposed to misreporting. In fact, it may be difficult for families to
ask teachers to falsify attendance records simply because someone else in another
school has been warned. Third, children have several different teachers who have to
register attendance: bribing or convincing all of them may not be easy in the presence of generally high stakes.22 In fact, municipalities face important incentives for
proper monitoring and reporting of school attendance: since 2005 the Ministry of
Social Development (MDS) has exerted massive efforts to strengthen the monitoring of conditionalities, introducing mechanisms to promote incentives for quality
management and rewarding innovations in the decentralized management of BFP
(Lindert et al., 2007).
Taken all the evidence together, our results suggest that families respond to
the enforcement of program conditions and that at least an important part of their
behavioral response corresponds to an actual increase in terms of school attendance.
To summarize our results so far, we have shown that the receipt of warnings
reduces the likelihood that households fail to comply with the 85 percent school
attendance requirement. We provided evidence that this effect can be interpreted as
21
Unfortunately, we cannot directly test for misreporting, differently from Linden and Shastri
(2012) who rely on external monitors’ verification in a sample of Indian schools.
22
Teachers earn a relatively high salary and it is unclear that parents from poor households could
offer a sufficiently large amount of money to induce teachers to falsify records and risk complaints
by other students or teachers, and/or risk punishment by the school principal.
20
causal, i.e. that the increase in school attendance is a response to the warning. We
now move to the main focus of this paper, namely the question of whether people
not only respond to experiencing enforcement themselves, but also learn about the
strictness of enforcement from warnings of their peers.
5
Peers’ Experience of Enforcement
In this section we analyze whether BFP beneficiaries learn about enforcement from
the experiences of peers who receive warnings. In particular, children who are in
the same class as one’s own children and their parents are likely to be key sources of
information regarding the implementation of the program. To explore these effects
we rely on individual children as the unit of observation and construct different
sets of peers, comprising the child’s own classmates and the classmates of a child’s
siblings.
5.1
Identification
Identifying the impact of the warnings received by classmates is a non-trivial issue.
To discuss our empirical strategy it is useful to start from a simple specification,
which is not the one we estimate, but which helps highlight identification challenges. Consider the following model:
Yiht =
5
X
k
αk WS ht
+ β PEERWARNiht + γXiht + Dt + Di + iht
(3)
k=1
where i denotes the child, h the household, t the month; Y is an indicator for whether
child i failed to comply in month t, WS k is a set of dummies to denote if the household is in warning stage k; X is a vector of child level controls including age and
number of brothers and sisters in different age brackets (6-10, 11-15, 16-18); Dt denotes month and year fixed effects; Di denotes child fixed effects and is the error
term. The key regressor of interest is PEERWARNiht , which is the fraction of i’s
classmates who receive a warning in month t.
Suppose we found –as we do– a negative correlation between a child’s failure to
21
attend in a given month and the fraction of peers who are warned (b
β < 0). Before we
can interpret this correlation as learning we need to address several identification
challenges.
Correlated shocks. The first threat to identification are correlated shocks that
may directly affect a student and her peers, thus inducing a correlation between
PEERWARNiht and iht in equation (3). Consider for example an economic shock
leading to an increase in the opportunity cost of schooling in the area where individual i lives. In response to such a shock, both individual i and her peers would be
more likely not to comply and thus more likely to receive a warning.23
If the shock was persistent, it would induce individual i and her peers to still not
comply several months later, when the warning is received. However, this type of
mechanism would generate a positive, not negative, correlation between a child’s
noncompliance and her peers’ warnings (b
β > 0), while what we find in the data is a
negative correlation (b
β < 0).
If, on the other hand, the shock was mean-reverting, this would lead to a negative correlation between a child’s noncompliance and her peers’ warnings and could
thus be confounded with the learning interpretation we offer. To address this concern, we include the lead of peers’ warnings as a falsification test, i.e., we add
PEERWARNih,t+1 among the controls in equation (3). Our reasoning exploits the
time lag from the moment in which noncompliance occurs and the moment in which
the warning arrives (as discussed in section 2, this delay has a median value of 3
months and a mean of 3.8 months). If a child’s attendance increases because of
mean-reversion after the initial instance of noncompliance, there is no reason why
the attendance would start reverting to the mean with the exact same delay as the
warnings of her peers, which vary between 2 and 6 months. In the case of meanreversion, one would typically expect changes in attendance to start occurring before the arrival of the warnings, which implies that we should find a negative and
significant coefficient on PEERWARNih,t+1 . Failing to find an effect of the lead variable would be hard to reconcile with the interpretation of mean-reverted shocks: it
23
To address the concern that the arrival of an individual’s own warning might be correlated
with the arrival of her peers’ warnings, we always control for own warnings and analyze if peers’
warnings have an additional effect.
22
would mean that the initial shock, which led to noncompliance, starts reverting exactly, say, four months afterwards (when peers happen to receive the warning) but
not three months afterwards.
An additional strategy we employ to deal with grade or school-specific correlated shocks is to exploit warnings received not only by individual i’s own classmates, but by the classmates of i’s siblings. Since siblings typically have different
ages, the effect of warnings received by siblings’ peers should not reflect class or
grade-specific shocks. This should be particularly true for a second specification
we use, in which we focus on peers of siblings in other schools (being in different
schools is mostly due to siblings’ age difference). The warnings received by students of those schools should not be correlated with shocks experienced by child i’s
own school, conditional on the warnings of the child’s family and of her own peers.
On the other hand, warnings received by siblings’ peers do contain information
about the quality of BFP enforcement. We include the maximum fraction of peers
who got warned across child i’s siblings, as the strongest signal of enforcement.24
Conventional peer effects. A separate concern relates to direct or ‘conventional’ peer effects. As we have shown in the first part of the paper, once an individual receives a warning, she reacts by reducing the likelihood of noncompliance (i.e.
increasing attendance). This means that when a child’s classmates receive warnings, they will attend school more in response to their own warnings. The child
may then start attending more because she observes her peers doing so. This response would imply a spillover effect of enforcement on peers’ school attendance,
but cannot necessarily be interpreted as learning about enforcement: it might be due
to learning about the benefits of schooling or to a preference to attend school with
more peers.
To identify “learning about enforcement” we pursue two approaches. First, we
directly control for the fraction of child i’s classmates who fail to comply with
conditionality, to analyze if warnings of i’s peers have an independent effect on i’s
likelihood to fail.25 Second, we analyze whether the probability that child i fails
24
The more families in a class receive a warning, the more likely it is that this becomes a topic of
discussion among children and parents of beneficiary households.
25
This may lead to an underestimate of the “true” learning effect, if part of the learning about
23
to comply decreases when her siblings’ peers (possibly at a different school) get
warned. Since those peers are not child i’s classmates (or not even in child i’s
school), the direct effect of their school attendance should not be important. On the
other hand, warnings received by siblings’ peers contain relevant information about
the strictness of enforcement.
To sum up, the two specifications we estimate are:
Yiht =
5
X
0
X
k
αk WS ht
+
n=−1
k=1
0
X
βn PEERWARNih,t+n +
ζ n PEERFAILih,t+n +γXiht +Dt +Di + iht
n=−1
(4)
Yiht =
5
X
k
αk WS ht
k=1
+
0
X
βn PEERWARNih,t+n +
n=−1
0
X
δn MaxPEERWARNih,t+n + γXiht + Dt
n=−1
+ Di + iht
(5)
where PEERFAILih,t+n is the fraction of i’s classmates who are BFP recipients and
fail to comply in month t; MaxPEERWARNih,t is the maximum fraction of classmates who got warned in month t among i’s siblings. This variable is constructed
alternatively from all of i’s siblings or from siblings who attend a different school
than i. For both peers’ warnings and peers’ noncompliance we augment the specification with a one-month lag, because it is ex ante difficult to say how persistent the
effects may be. We estimate equations (4) and (5) using a linear probability model
and clustering the standard errors at the household level (or, as a robustness check,
at the school level).
5.2
Main results
Table 4 reports our main results on classmates’ warnings. The coefficient on the
fraction of classmates warned in column 1 is −0.011 for the contemporaneous variable and −0.023 for the lagged one, both significant at the 1 percent level. This
indicates that after more classmates receive a warning, the child is less likely to fail
enforcement happens through observing one’s peers’ higher attendance.
24
to comply with the attendance requirement. To assess the magnitude of the effect
in relation to the mean: if all of i’s classmates who are BFP recipients received a
warning in a given month, child i’s noncompliance would decrease by 13 percent
in the same month and 27.5 percent in the following month. 26
[Insert Table 4]
In column 2 we include the fraction of classmates warned as lead variable to
conduct a falsification test and rule out the importance of correlated shocks and
mean reversion. As explained above, if mean reversion were driving our results, we
would expect a negative coefficient on the lead of classmates’ warnings. We find
instead a precisely estimated zero, lending support to our interpretation.
In column 3 we control for the fraction of classmates who fail to meet the attendance threshold and find that both the contemporaneous and the lagged variable
are positively correlated with own noncompliance. At the same time, we still find a
negative effect of classmates’ warnings that is equally significant and comparable in
size to that of the previous specifications. Again, this is consistent with our learning
interpretation and suggests that ‘conventional’ peer effects operating through peers’
attendance are not driving our results.
In the remaining part of table 4 we focus on warnings received by siblings’
peers. For this analysis we naturally need to restrict the sample to children who
have at least one sibling in the age range of BFP conditionality. It turns out that
a large fraction of our original sample satisfies this condition, but in column 4 we
report our benchmark estimates for the reduced sample to show that the magnitude
of the coefficients is virtually the same as in column 1.
Column 5 shows that not only an individual’s own peers but also her siblings’
peers matter for her attendance decision: both the contemporaneous and the lagged
fraction of siblings’ classmates warned significantly reduces a child’s likelihood not
to comply, while controlling for the warnings of the child’s own classmates. The
results remain significant and comparable in size for the lag when we exclusively
focus on siblings going to a different school (column 6), while the coefficient on
26
Appendix table A.8 presents the same results as table 4, but displays in addition the coefficients
on the family’s own warning stage, which we control for in all specifications.
25
the contemporaneous variable is also negative but insignificant. The findings in
columns 5 and 6 lend further support to our learning interpretation, as the peers who
receive warnings in columns 5 and 6 are attending different grades or schools and
are exposed to different shocks. In Appendix table A.9 we present results clustering
standard errors at the school level. Standard errors remain virtually unchanged.
5.2.1
Interpretation: informational content of different warnings
To gain further insights into the role played by the new information contained in
warnings, we analyze how the effect of classmates’ warnings varies depending on
the peers’ warning stage relative to the family’s own warning stage. We expect that
warnings received by peers who are in a lower warning stage than the family’s own
should carry relatively less information, because the family has already experienced
first hand that the government enforces the program up to that level. On the other
hand, warnings of a level higher than one’s own carry new information, because
the family could still hold a prior that the government punishes up to some point,
but will not go through with more severe and costly punishments. Peers’ warnings
of the same stage as the family’s could still have an effect, for example, if other
families receive them earlier in the month or because they improve the precision of
the signal.
[Insert Table 5]
In Table 5 we distinguish between classmates who receive warning 1, 2, ...5 (the
variables listed by row) and estimate four different regression equations, conditional
on whether a family is currently in warning stage 1, 2, 3 or 4 (the different columns).
Clearly, all stages higher than one’s own should be relevant, but the next stage might
be particularly important for at least two reasons. First, in our data, the higher
the warning stage, the fewer the households that reach it. This implies that more
households receive a warning for the next stage, compared to subsequent warnings.
Second, if people are present-oriented, the closer in the future is the punishment,
the more they care about it.
The estimates in Table 5 lend support to our hypothesis that warnings received
by peers in higher warning stages have a stronger impact on school attendance
26
than warnings for the same or lower warning stage. For example, in column 1 the
coefficient on peers’ warnings for stage 2 is twice as large as that for stage 1. In
column 2 the coefficient on peers’ warnings for stage 3 is about one and a half
times as large as for stage 2 (similarly for column 3). Only in column 4 we find that
while the coefficient of peers’ warnings for stage 4 is significant, the one for stage
5 is not, which is likely due to the fact that extremely few families reach warning
stage 5 at all. Overall, these results corroborate our interpretation of learning about
enforcement, as it would be difficult to find alternative explanations that produce
the asymmetric pattern that we uncover.
5.2.2
Interpretation: different peers
While classmates are an important source of information about the strictness of
enforcement, another potential source are adults who are BFP beneficiaries and
who live in the same area. We hypothesize that families who receive warnings may
interact directly, and not only through their children in schools, and focus on a
dimension of interaction for which we can find exogenous variation.
Consider the interaction among adults living in the same neighborhood. These
adults and their families may experience common shocks and hence their children’s
attendance behavior may be correlated. However, as we explained in section 2,
the day of the month in which households receive warnings is determined by the
last digit of the social security number (NIS) of the designated household member.
Since this number is as good as random, the set of families living in a given zip code
who receive the warning on the same day is also as good as random. Why would
this be relevant from an information point of view? Households receive warnings
when they pick up the transfer from the local Caixa service point.27 Households that
visit the same Caixa point on the same day are more likely to meet and communicate
about warnings on the day when any information about enforcement is most salient.
We thus test whether compliance of a household is affected by warnings received
by other households that live in the same zip code and cash the transfer on the same
27
Kumar et al (2006) report that in the early 2000’s Caixa started expanding their banking correspondent network to reach even remote locations, and that by 2008 (the period studied in this paper)
there was roughly one Caixa correspondent per zip code.
27
day, conditional on warnings received by all households in the neighborhood. We
estimate the following specification:
Yiht =
5
X
k=1
k
αk WS ht
+
0
X
βn BANKWARNih,t+n +
0
X
ζ n NEIGHBORWARNih,t+n
n=−1
n=−1
+ δNEIGHBORS iht + γXiht + Dt + Di + iht
(6)
where all variables are defined as in equation (3), except for the following. We denote the number of BFP beneficiaries in i’s zip code in month t as NEIGHBORS iht ,
while NEIGHBORWARNiht denotes the fraction of BFP beneficiaries living in
i’s zip code who receive a warning in month t. The key regressor of interest is
BANKWARNiht , which is the fraction of BFP beneficiaries living in i’s zip code
who receive a warning in month t among those whose families can pick up the
transfers at the local Caixa point on the same day. By construction, this variable is
not based on a peer group which is chosen endogenously.
[Insert Table 6]
Table 6 reports the results. Column 1 shows that there is indeed a strongly significant negative relation between the fraction of BFP beneficiaries from the same
zip code who can pick up their transfers on the same day and individuals’ decision
of noncompliance. Based on our estimates, if 10 percent of the BFP recipients who
live in the same zip code and can pick up their transfers on the same day received a
warning, a child’s probability of noncompliance would decrease by 3.2 percent in
the same month and 6.3 percent in the following month.
In column 2 we include BANKWARN as lead variable to conduct a falsification
test and rule out the importance of correlated shocks and mean reversion. The
coefficient on the lead variable is a precisely estimated zero (with a coefficient of
−0.0007), lending support to our learning interpretation.
In column 3 we control for the fraction of BFP beneficiaries from the same
neighborhood who are warned in a given month (NEIGHBORWARN). The fraction of neighbors who are warned on the same day (BANKWARN) is exogenous
28
when controlling for the overall fraction of neighbors warned within that month, as
discussed above. We find that NEIGHBORWARN is positively correlated with an
individual’s noncompliance, while the lag of this variable is negatively correlated,
which might be due to correlated shocks that have some persistence but meanrevert at some point. More importantly, controlling for NEIGHBORWARN does
not change our key result, which is that a larger fraction warned on the same day
significantly decreases an individual’s likelihood of noncompliance. The point estimates imply that if 10 percent of the BFP recipients who live in the same zip code
and can pick up their transfers on the same day received a warning, a child’s probability of noncompliance would decrease by 4.1 percent in the same month and 3.2
percent in the following month.28
We also analyzed how the effect of other households’ warnings varies depending
on their warning stage relative to the family’s own warning stage. Analogous to our
analysis in section 5.2.1, we find that warnings received by other households who
live in the same zip code, can pick up their transfer on the same day and are in
higher warning stages have a stronger impact on compliance than warnings for the
same or lower warning stage. This is consistent with our learning interpretation:
warnings for lower stages than one’s own carry relatively less information, because
the family has already experienced them. The results are reported in Appendix
Table A.11.29
Overall, the fact that we find consistent effects for two different types of peers
that are based on two entirely different identification strategies (partially overlapping networks in the case of classmates and quasi-random variation in the case of
28
In Appendix table A.10 we present results clustering standard errors at the zip-code level. Standard errors are somewhat larger, but all conclusions are unchanged. In particular, the coefficients on
the main variable of interest, i.e. on the ”fraction of neighbors warned on the same day”, and on its
lag are all significant at the one percent level.
29
In Appendix Table A.11, for households that are in stage 1 (column 1) the coefficients on other
households’ warnings for stages 2 and 3 are three and five times larger, respectively, than that for
stage 1 (the difference is significant at the 2 and 1 percent level, respectively). In column 2 the
coefficient for stage 3 is similar as for stage 2, but the one for stage 4 is more than four times
larger (the difference is significant at the 10 percent level). Only in columns 3 and 4 we do not find
significant differences, possibly due to the fact that the punishment in the case of the fourth warning
is in fact the same as in the case of the third warning, while extremely few families reach warning
stage 5 at all.
29
households living in the same zip code), strengthens our confidence in the validity
of our approach and interpretation.
6
Conclusions
In this paper we study the implementation of the large-scale conditional cash transfer program “Bolsa Familia” in Brazil. This program conditions transfers to poor
families on children’s school attendance: when families fail to comply with this
requirement, they receive a series of warnings and financial penalties. We analyze
how people learn about and respond to the enforcement of program conditions. We
find that warnings not only have a direct effect on the families warned, but also important spillover effects on other families, who learn from the experiences of their
children’s classmates and from other households living nearby who are warned on
the same day.
Our finding that people adjust their behavior to the strictness of enforcement
implies that not only formal rules but actual enforcement of program conditions
is crucial for program effectiveness. This aspect seems particularly important for
developing countries, as they might lack administrative capacity or political will to
strictly enforce the rules.30 Thus the design of conditional welfare programs should
take into account the important dimensions of monitoring and enforcement.
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30
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34
APPENDIX
Figure 1: Timing of Noncompliance and Warning
Figure 2: Response to warning
.15
Fraction Noncompliant
.2
.25
.3
Response to Warnings
−1
0
1
2
3
Months since Warning
4
5
®
Warning
35
Figure 3: Response to warning, by delay
Response to Warnings with Different Delays
.1
.1
.1
Fraction Noncompliant
.2 .3 .4 .5 .6 .7
Delay of 4 Months
Fraction Noncompliant
.2 .3 .4 .5 .6 .7
Delay of 3 Months
Fraction Noncompliant
.2 .3 .4 .5 .6 .7
Delay of 2 Months
Noncompl. Warning
0
1
2
3
4
5
6
Noncompl.
0 1
5
6
7
Noncompl.
0 1 2
Warning
3 4 5
6
7
8
Delay of 6 Months
.1
.1
Fraction Noncompliant
.2 .3 .4 .5 .6 .7
Fraction Noncompliant
.2 .3 .4 .5 .6 .7
Delay of 5 Months
Warning
2 3 4
Noncompl.
Warning
0 1 2 3 4 5 6 7 8 9
Noncompl.
Warning
0 1 2 3 4 5 6 7 8 9 10
®
Table 1: Summary statistics
Variable
A. Own Warnings
Noncompliance
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Warned
Delay of Warnings
B. Peer Warnings
Frac of Classmates Warned
Frac of Classmates Noncompl.
No of Peers in School
No of Peers in Grade
No of Peers in Class
Observations
Mean
Std. Dev.
8090769
8090769
8090769
8090769
8090769
8090769
8090769
267626
0.086
0.292
0.085
0.029
0.011
0.002
0.035
3.809
0.280
0.455
0.279
0.169
0.103
0.041
0.184
1.398
5914381
5914381
5914381
5914381
5914381
0.014
0.010
279.407
51.970
16.533
0.059
0.046
222.976
50.544
6.752
36
Table 2: Effect of own warnings on attendance
Dependent Variable:
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Household FE
Time FE
No. Obs.
R-squared
Noncompliance
(in a Given Month)
-0.0624***
(0.0000)
-0.1303***
(0.001)
-0.2050***
(0.002)
-0.2656***
(0.003)
-0.3477***
(0.008)
Yes
Yes
Yes
8,090,769
0.23
Notes: Robust standard errors in parentheses (clustered at the household level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: fraction of male children, number
of boys and girls in the household in the age
categories 6 to 10, 11 to 15, and 16 to 18,
month and year dummies and household fixed
effects.
37
Table 3: Effect of own warnings, random variation in timing
Dependent Variable:
Timing:
Warning Stage 1 * Timing
Warning Stage 2 * Timing
Warning Stage 3 * Timing
Warning Stage 4 * Timing
Warning Stage 5 * Timing
Lag Warning Stage 1 * Timing
Lag Warning Stage 2 * Timing
Lag Warning Stage 3 * Timing
Lag Warning Stage 4 * Timing
Lag Warning Stage 5 * Timing
Controls
Household FE
Time FE
No. Obs.
R-squared
Noncompliance in a Given Month
Early
Late
Diff (Early-Late)
Coeff/(S.E.) Coeff/(S.E.)
Diff/[p-val]
-0.0253*** -0.0112***
-0.0141
(0.001)
(0.001)
[0.0000]
-0.0474*** -0.0052***
-0.0422
(0.002)
(0.002)
[0.0000]
-0.1267*** -0.0633***
-0.0634
(0.004)
(0.003)
[0.0000]
-0.1887*** -0.1168***
-0.0719
(0.007)
(0.006)
[0.0000]
-0.1641*** -0.0955***
-0.0686
(0.016)
(0.013)
[0.0002]
-0.0356*** -0.0484***
(0.001)
(0.001)
-0.0895*** -0.1230***
(0.002)
(0.002)
-0.0930*** -0.1438***
(0.004)
(0.003)
-0.0877*** -0.1513***
(0.007)
(0.006)
-0.2134*** -0.2715***
(0.018)
(0.015)
Yes
Yes
Yes
7,551,546
0.23
0.0128
[0.0000]
0.0335
[0.0000]
0.0508
[0.0000]
0.0636
[0.0000]
0.0581
[0.0086]
Notes: ”Early” (”Late”) indicates households that withdraw the transfer -and receive
warnings, if applicable- in the first (second) half of the withdrawing period during
a month. Robust standard errors in parentheses (clustered at the household level).
*** p<0.01, ** p<0.05, * p<0.1. Included controls are: fraction of male children,
number of boys and girls in the household in the age categories 6 to 10, 11 to 15,
and 16 to 18, month and year dummies. All specifications include household fixed
effects.
38
Table 4: Effect of classmates’ warnings
Dependent Variable:
Sample
Benchmark
Fraction of Classmates Warned
Lag of Frac of Classmates Warned
(1)
-0.0112***
(0.002)
-0.0231***
(0.002)
Lead of Frac of Classmates Warned
Fraction of Classmates Noncompliant
Lag of Frac of Classmates Noncompliant
39
Max Frac of Siblings’ Classmates Warned
Lag Max Frac of Siblings’ Classmates Warned
Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Lag Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Controls for Own Warning Stage
Controls
Individual FE
Time FE
No. Obs.
R-squared
Yes
Yes
Yes
Yes
5,914,114
0.28
Noncompliance in a Given Month
All Children
Children with Siblings
Placebo
Control for
Benchmark Siblings’ Classmates Siblings’ Classmates
Peers’ Noncompl.
Other Schools
(2)
(3)
(4)
(5)
(6)
-0.0120***
-0.0100***
-0.0106***
-0.0085***
-0.0099***
(0.002)
(0.002)
(0.002)
(0.003)
(0.003)
-0.0236***
-0.0199***
-0.0227***
-0.0189***
-0.0191***
(0.002)
(0.002)
(0.002)
(0.002)
(0.003)
0.0001
(0.002)
0.2807***
(0.021)
0.0952***
(0.009)
-0.0047**
(0.002)
-0.0076***
(0.002)
-0.0013
(0.002)
-0.0061**
(0.003)
Yes
Yes
Yes
Yes
5,628,700
0.27
Yes
Yes
Yes
Yes
5,914,114
0.28
Yes
Yes
Yes
Yes
4,902,847
0.28
Yes
Yes
Yes
Yes
4,902,847
0.28
Yes
Yes
Yes
Yes
4,902,847
0.28
Notes: Robust standard errors in parentheses (clustered at the household level). *** p<0.01, ** p<0.05, * p<0.1. Included controls are: age dummies, birth order
dummies, number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18, month and year dummies. All specifications include individual fixed
effects.
Table 5: Information content of classmates’ warnings
Dependent Variable:
Own Warning Stage:
Frac Classmates Warned (WS 1)
Frac Classmates Warned (WS 2)
Frac Classmates Warned (WS 3)
Frac Classmates Warned (WS 4)
Frac Classmates Warned (WS 5)
Controls
Individual FE
Time FE
No. Obs.
R-squared
Noncompliance in Given Month
1
2
3
4
-0.0123***
-0.0139
-0.0118
0.0318
(0.003)
(0.009)
(0.016)
(0.028)
-0.0245*** -0.0203**
-0.0171
-0.0693
(0.007)
(0.009)
(0.033)
(0.044)
-0.0188
-0.0308* -0.0501**
-0.0392
(0.012)
(0.017)
(0.021)
(0.051)
-0.0197
-0.0386
-0.0787* -0.0590**
(0.022)
(0.026)
(0.043)
(0.027)
0.0274
0.0840
0.0392
0.1151
(0.036)
(0.070)
(0.088)
(0.123)
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
1,993,576
639.362
232.623
88.697
0.46
0.52
0.52
0.54
Notes: Robust standard errors in parentheses (clustered at the household level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: age dummies, birth order dummies,
number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18, month
and year dummies.
40
Table 6: Effect of warnings of neighbors in the bank
Dependent Variable:
Frac in Bank Warned
Lag of Frac in Bank Warned
Lead of Frac in Bank Warned
Frac Neighbors Warned
Lag of Frac Neighbors Warned
No of BFP Neighbors
Controls for Own Warning Stage
Controls
Individual FE
Time FE
Observations
R-squared
Noncompliance in Given Month
Benchmark
Placebo
Controls for
Neighbors Warned
(1)
(2)
(3)
-0.0275*** -0.0275***
-0.0349***
(0.004)
(0.004)
(0.006)
-0.0548*** -0.0547***
-0.0284***
(0.003)
(0.003)
(0.004)
0.0007
(0.004)
0.0164*
(0.009)
-0.0609***
(0.007)
-0.0000*** -0.0000***
-0.0000***
(0.000)
(0.000)
(0.000)
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
4,813,029
4,813,029
4,813,029
0.21
0.21
0.21
Notes: Robust standard errors in parentheses (clustered at the household level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: age dummies, birth order dummies,
number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18,
month and year dummies and individual fixed effects.
41
Online Appendix – Not For Publication
A. Difference-in-Difference Analysis
Further insights into the causal nature of the estimates can be gained by making use
of variation in the delay of warnings across months. As discussed, the variation in
delay is almost entirely explained by time and area fixed effects and there is no correlation with household or child characteristics. We thus estimate a difference-indifferences model that is the regression counterpart of figures 2 and 3. In particular,
we compare two groups of households: both groups failed to comply in the same
month, but they receive their warnings with different delays. We then compare the
behavior of households who have already been warned (the “treated” households)
with those who have not yet received their warning (controls). Let “Post” be an indicator taking value 1 in the calendar month(s) after the warning of the households
receiving the earlier warnings and 0 otherwise. We estimate:
Yht = α · T reatedht + β · Postht + γ(T reatedht · Postht ) + δXht + Dt + Dh + ht . (7)
Our coefficient of interest is γ, which we expect to be negative if households react
to warnings by decreasing noncompliance (i.e. increasing attendance) of their children. The results are reported in Appendix Table A.6 using different time horizons
for pre- and post-warning.
[Insert Appendix Table A.6]
In the first column, we consider an interval of three months around a warning
and let “Post” take value 1 in the month following the warning, and 0 in the month
of the warning and the month before. The estimated coefficient suggests that households who receive a warning decrease their noncompliance rate by 3.8 percentage
points compared to households that have not yet received their warning. This represents almost a 30 percent decrease over the mean. The estimates are of a similar
order of magnitude if we expand the analysis to a period of five months around a
42
warning and define as “Post” the two months following the warning: the estimated
coefficient in that case is −0.045, significant at the 1 percent level.
To provide further evidence that this is actually identifying a behavioral response to the warning, we show that pre-trends are the same for both groups supportin the common trend assumption underlying our difference-in-difference analysis. In columns 3 and 4 we conduct the following falsification tests. We define as
“Post” the month of the warning and use as pre-period the month before (column
3) or the two months before (column 4). If our negative estimate were picking up a
differential trend for warned households, this would result in a negative coefficient
on “Treated∗Post” in columns 3 and 4. The fact that we instead obtain small and insignificant coefficients on the interaction term lends credibility to the interpretation
that our effect is a causal response to the receipt of the warning.
43
B. Appendix Figures and Tables
Figures
Figure A.1: Frequency of delays
0
.1
Fraction of Warnings
.2
.3
.4
Delay of Warning Receipt
2
3
4
Delay (in Months)
5
6
®
i
Figure A.2: Response to warning, by warning stage
Response to Warnings
5
Fraction Noncompliant
.2
.3
Warning
−1 0
1
2
3
4
Months since Warning
5
Warning
−1 0
1
2
3
4
Months since Warning
5
Fraction Noncompliant
.1
.2
.3
Warning Stage 5
Fraction Noncompliant
.2
.3
Warning
−1 0
1
2
3
4
Months since Warning
.1
.1
.1
Warning
−1 0
1
2
3
4
Months since Warning
Warning Stage 4
.1
Warning Stage 3
Fraction Noncompliant
.2
.3
Warning Stage 2
Fraction Noncompliant
.2
.3
Warning Stage 1
5
Warning
−1
0
1
2
3
4
Months since Warning
5
®
ii
Tables
Table A.1: Summary statistics
Variable
Own Warnings
Noncompliance
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Warned
Delay of Warnings
Frac Male
N of Sisters 6 to 10
N of Brothers 6 to 10
N of Sisters 11 to 14
N of Brothers 11 to 14
N of Sisters 15 to 17
N of Brothers 15 to 17
Month
Year 2009
Parents informed in Writing
Parents informed in Meetings
Parents informed in Home Visits
Peer Warnings
Frac of Peers Warned
Frac of Peers Noncompl
Max Fraction of Siblings’ Peers Warned
All Siblings
Siblings in Other Schools
N of Peers in School
N of Peers in Grade
N of Peers in Class
Predetermined Characteristics
Head Female
Head Married
Head Single
Head Age
Head White
Head Yrs of Educ
Head Working
Spouse Age
Spouse White
Spouse Yrs of Educ
Spouse Working
Dep Ratio
Pct Indio
HH Expenditures
House Property
Garbage Collected
Running Water
Electricity
iii
Observations
Mean
Std. Dev.
8090769
8090769
8090769
8090769
8090769
8090769
8090769
267626
8090769
8090769
8090769
8090769
8090769
8090769
8090769
8090769
8090769
5044299
5044299
5044299
0.086
0.292
0.085
0.029
0.011
0.002
0.035
3.809
0.530
0.206
0.222
0.250
0.271
0.154
0.172
6.538
0.492
0.790
0.940
0.703
0.280
0.455
0.279
0.169
0.103
0.041
0.184
1.398
0.387
0.386
0.400
0.412
0.432
0.340
0.360
2.864
0.500
0.408
0.169
0.457
5914381
5914381
0.014
0.010
0.059
0.046
4903020
4903020
5914381
5914381
5914381
0.014
0.013
279.407
51.970
16.533
0.058
0.058
222.976
50.544
6.752
478511
478511
478511
478511
478511
478511
478511
261318
261318
261318
261318
478511
478511
478511
478511
478511
478511
478511
0.933
0.337
0.531
38.063
0.182
4.517
0.510
40.924
0.167
3.519
0.738
1.092
0.002
2254.6
0.695
0.594
0.610
0.793
0.249
0.468
0.495
10.028
0.384
3.227
0.487
10.536
0.371
3.057
0.430
1.033
0.040
15356.5
0.453
0.487
0.482
0.398
Table A.2: Effect of own warnings, individual level
Dependent Variable:
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Individual FE
Time FE
No. Obs.
R-squared
Noncompliance
(in a Given Month)
-0.0336***
(0.0000)
-0.0657***
(0.001)
-0.0970***
(0.001)
-0.1147***
(0.002)
-0.1366***
(0.005)
Yes
Yes
Yes
16,056,547
0.23
Notes: Robust standard errors in parentheses (clustered at the household level). *** p<0.01, ** p<0.05,
* p<0.1. Included controls are: age dummies, birth
order dummies, number of brothers and sisters in the
age categories 6 to 10, 11 to 15, and 16 to 18, month
and year dummies and individual fixed effects.
iv
Table A.3: Correlates of delay
Dependent Variable:
Delay of Warning
(2)
Coeff
(Std.Err.)
-0.0009
(0.001)
-0.0005
(0.001)
0.0019
(0.001)
-0.0009
(0.001)
-0.0019
(0.002)
0.0002
(0.001)
0.0006
(0.002)
-0.0033
(0.004)
-0.0026
(0.004)
0.0009
(0.002)
0.0001
(0.000)
0.0000
(0.000)
0.0001
(0.001)
-0.0003
(0.002)
0.0001
(0.000)
0.0000
(0.000)
-0.0009
(0.001)
0.0001
(0.001)
0.0000
(0.000)
-0.0023*
(0.001)
-0.0004
(0.001)
-0.0012
(0.001)
-0.0009
(0.001)
Yes
Yes
Yes
Yes
(1)
N of Girls 6 to 10
N of Boys 6 to 10
N of Girls 11 to 14
N of Boys 11 to 14
N of Girls 15 to 17
N of Boys 15 to 17
Head Female
Head Married
Head Single
Head White
Head Age
Head Yrs of Educ
Head Work
Spouse White
Spouse Age
Spouse Yrs of Educ
Spouse Work
Dependency Ratio
Expenditures
House Property
Garbage Collection
Water Connection
Electricity
Time FE
Municipality FE
P-val of F-test
(joint sig of HH charac)
Observations
R-squared
267,626
0.98
0.910
111,462
0.98
Notes: Robust standard errors in parentheses (clustered at the
household level). *** p<0.01, ** p<0.05, * p<0.1.
v
Table A.4: Effect of own warnings, by highest warning stage reached
Dependent Variable
Highest WS Reached
1
Warning Stage 1
-0.1863***
(0.001)
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Time FE
Household FE
P-Values of Tests:
Coeff of WS 1 vs 2
Coeff of WS 2 vs 3
Coeff of WS 3 vs 4
Coeff of WS 4 vs 5
No. Obs.
R-Squared
Yes
Yes
Yes
2,977,415
0.14
Noncompliance in a Given Month
2
3
4
5
-0.1677*** -0.1716*** -0.1385*** -0.1464***
(0.002)
(0.004)
(0.009)
(0.027)
-0.5120*** -0.4907*** -0.2874*** -0.2960***
(0.003)
(0.005)
(0.012)
(0.035)
-0.9837*** -0.7029*** -0.6010***
(0.006)
(0.017)
(0.048)
-1.1119*** -0.8757***
(0.020)
(0.059)
-1.2264***
(0.072)
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
0.000
0.000
0.000
0.000
0.000
0.000
814,758
0.21
221,764
0.27
55,233
0.27
0.000
0.000
0.000
0.000
8,350
0.27
Notes: Initial warning stage is 0 (i.e. warning stage at the beginning of our period of observation, namely January
2008). Robust standard errors in parentheses (clustered at the household level). *** p<0.01, ** p<0.05, * p<0.1.
Included controls are: fraction of male children, number of boys and girls in the household in the age categories
6 to 10, 11 to 15, and 16 to 18, month and year dummies. All specifications include household fixed effects.
vi
Table A.5: Balance test
Timing:
Time-Varying Characteristics
N of Sisters 6 to 10
N of Brothers 6 to 10
N of Sisters 11 to 14
N of Brothers 11 to 14
N of Sisters 15 to 17
N of Brothers 15 to 17
No. Obs.
Pre-Program Characteristics
Head Married
Head Single
Head Female
Head Age
Head White
Head Years of Education
Head Work
Spouse Age
Spouse White
Spouse Years of Education
Spouse Work
Dependency Ratio
Pct Indio
Expenditure
House Property
Garbage Collected
Water Connection
Electricity
No. Obs.
Early
Mean/SE
Late
Mean/SE
Diff/[p-val]
0.1643
(0.3432)
0.1738
(0.3529)
0.1894
(0.3643)
0.1949
(0.3708)
0.1157
(0.2984)
0.1186
(0.3017)
3,021,032
0.1644
(0.3421)
0.1738
(0.3521)
0.1902
(0.3654)
0.1948
(0.3687)
0.1142
(0.2953)
0.1191
(0.3037)
4,530,514
-0.0001
[0.588]
-0.0001
[0.755]
-0.0009
[0.002]
0.0001
[0.617]
0.0014
[0.000]
-0.0003
[0.184]
7,551,546
0.3366
(0.4683)
0.5333
(0.4951)
0.9351
(0.2457)
38.0615
(10.0252)
0.1821
(0.3839)
4.5259
(3.2404)
0.5114
(0.4870)
40.9540
(10.5281)
0.1653
(0.3697)
3.5286
(3.0540)
0.7389
(0.4299)
1.0941
(1.0307)
0.0016
(0.0389)
2099.51
(15129.77)
0.6946
(0.4538)
0.5931
(0.4878)
0.6115
(0.4815)
0.7937
(0.3976)
188,970
0.3383
(0.4689)
0.5321
(0.4950)
0.9336
(0.2480)
38.0472
(10.0127)
0.1819
(0.3836)
4.5145
(3.2181)
0.5079
(0.4874)
40.9009
(10.5078)
0.1686
(0.3725)
3.5158
(3.0580)
0.7395
(0.4294)
1.0903
(1.0354)
0.0017
(0.0402)
2227.50
(15070.91)
0.6953
(0.4533)
0.5946
(0.4874)
0.6096
(0.4822)
0.7925
(0.3984)
284,527
-0.0017
[0.221]
0.0012
[0.429]
0.0015
[0.043]
0.0143
[0.630]
0.0003
[0.814]
0.0114
[0.251]
0.0036
[0.014]
0.0531
[0.209]
-0.0032
[0.035]
0.0127
[0.311]
-0.0006
[0.725]
0.0039
[0.207]
-0.0001
[0.452]
-127.987
[0.775]
-0.0007
[0.620]
-0.0016
[0.285]
0.0019
[0.192]
0.0012
[0.330]
472,029
Notes: ”Early” (”Late”) indicates households that withdraw the
transfer -and receive warnings, if applicable- in the first (second)
half of the withdrawing period during a month.
vii
Table A.6: Effect of own warnings, difference-in-differences
Treat * Post
Treat
Post
No. Obs.
R-squared
Main result
Definition 1
Definition 2
Warning: t=0
Warning: t=0
Before: t=-1,0 Before: t=-2,-1,0
Post: t=1
Post: t=1,2
-0.0379***
-0.0447***
(0.002)
(0.003)
0.0014
0.0061***
(0.001)
(0.002)
-0.1853***
-0.0153***
(0.001)
(0.002)
763,847
458,967
0.05
0.03
Placebo
Definition 1
Definition 2
Warning: t=0
Warning: t=0
Before: t=-1 Before: t=-2,-1
Post: t=0
Post: t=0
0.002
-0.0037
(0.003)
(0.003)
0.0021
0.0078***
(0.002)
(0.002)
-0.2642***
-0.0269***
(0.002)
(0.002)
458,224
309,942
0.06
0.03
Notes: Robust standard errors in parentheses (clustered at the household level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: fraction of male children, number
of boys and girls in the household in the age categories 6 to 10, 11 to 15, and 16 to 18,
month and year dummies.
viii
Table A.7: Learning about attendance
Dependent Variable:
Parents Informed in:
Warning Stage 1 * Parents Informed
Warning Stage 2 * Parents Informed
Warning Stage 3 * Parents Informed
Warning Stage 4 * Parents Informed
Warning Stage 5 * Parents Informed
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Household FE
Time FE
No. Obs.
R-Squared
Noncompliance in a Given Month
Writing
Meeting
Home Visit Benchmark
-0.0003
-0.0021
0.0002
(0.001)
(0.003)
(0.001)
-0.0008
-0.0039
0.0006
(0.003)
(0.007)
(0.002)
-0.0100**
0.0204
-0.0066
(0.005)
(0.013)
(0.005)
-0.0096
0.0472*
-0.0009
(0.009)
(0.024)
(0.009)
-0.0293
0.1017*
0.0159
(0.023)
(0.054)
(0.021)
-0.0619***
-0.0640***
(0.003)
(0.0000)
-0.1284***
-0.1324***
(0.006)
(0.001)
-0.2106***
-0.2034***
(0.013)
(0.002)
-0.3002***
-0.2626***
(0.024)
(0.004)
-0.4269***
-0.3401***
(0.051)
(0.0100)
Yes
Yes
Yes
Yes
Yes
Yes
5,044,299
5,044,299
0.24
0.24
Notes: Robust standard errors in parentheses (clustered at the household level). *** p<0.01, ** p<0.05, * p<0.1.
Included controls are: fraction of male children, number of boys and girls in the household in the age categories
6 to 10, 11 to 15, and 16 to 18, month and year dummies. All specifications include household fixed effects.
ix
Table A.8: Effect of classmates’ warnings
Dependent Variable:
Sample
Own Warnings
(1)
Fraction of Classmates Warned
Lag of Frac of Classmates Warned
Lead of Frac of Classmates Warned
Fraction of Classmates Failed
Lag of Frac of Classmates Failed
Max Frac of Siblings’ Classmates Warned
Lag Max Frac of Siblings’ Classmates Warned
x
Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Lag Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Individual FE
Time FE
No. Obs.
R-squared
-0.0110***
(0.000)
-0.0190***
(0.001)
-0.0229***
(0.001)
-0.0214***
(0.002)
-0.0249***
(0.004)
Yes
Yes
Yes
5,914,114
0.28
Noncompliance in a Given Month
All Children
Children with Siblings
Benchmark
Placebo
Control for
Benchmark
Siblings’ Peers
Siblings’ Peers
Peers’ Noncompl.
Other Schools
(2)
(3)
(4)
(5)
(6)
(7)
-0.0112***
-0.0120***
-0.0100***
-0.0106***
-0.0085***
-0.0099***
(0.002)
(0.002)
(0.002)
(0.002)
(0.003)
(0.003)
-0.0231***
-0.0236***
-0.0199***
-0.0227***
-0.0189***
-0.0191***
(0.002)
(0.002)
(0.002)
(0.002)
(0.002)
(0.003)
0.0001
(0.002)
0.2807***
(0.021)
0.0952***
(0.009)
-0.0047**
(0.002)
-0.0076***
(0.002)
-0.0013
(0.002)
-0.0061**
(0.003)
-0.0107***
-0.0110***
-0.0103***
-0.0092***
-0.0092***
-0.0092***
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
-0.0188***
-0.0192***
-0.0182***
-0.0175***
-0.0175***
-0.0175***
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
-0.0227***
-0.0232***
-0.0219***
-0.0222***
-0.0222***
-0.0222***
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
-0.0213***
-0.0213***
-0.0207***
-0.0217***
-0.0217***
-0.0217***
(0.002)
(0.002)
(0.002)
(0.002)
(0.002)
(0.002)
-0.0248***
-0.0270***
-0.0249***
-0.0242***
-0.0242***
-0.0242***
(0.004)
(0.004)
(0.004)
(0.004)
(0.004)
(0.004)
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Yes
5,914,114
5,628,700
5,914,114
4,902,847
4,902,847
4,902,847
0.28
0.27
0.28
0.28
0.28
0.28
Notes: Robust standard errors in parentheses (clustered at the household level). *** p<0.01, ** p<0.05, * p<0.1. Included controls are: age
dummies, birth order dummies, number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18, month and year dummies.
All specifications include individual fixed effects.
Table A.9: Effect of classmates’ warnings (clustering of standard errors at the school level)
Dependent Variable:
Sample
Own Warnings
(1)
Fraction of Classmates Warned
Lag of Frac of Classmates Warned
Lead of Frac of Classmates Warned
Fraction of Classmates Noncompliant
Lag of Frac of Classmates Noncompliant
Max Frac of Siblings’ Classmates Warned
Lag Max Frac of Siblings’ Classmates Warned
xi
Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Lag Max Frac of Siblings’ Classmates Warned
(Only Sibs at Other Schools)
Warning Stage 1
Warning Stage 2
Warning Stage 3
Warning Stage 4
Warning Stage 5
Controls
Individual FE
Time FE
No. Obs.
R-squared
-0.0111***
(0.000)
-0.0193***
(0.001)
-0.0231***
(0.001)
-0.0218***
(0.002)
-0.0248***
(0.004)
Yes
Yes
Yes
5,833,861
0.28
Noncompliance in a Given Month
All Children
Children with Siblings
Benchmark
Placebo
Control for
Benchmark
Siblings’ Peers
Siblings’ Peers
Peers’ Noncompl.
Other Schools
(2)
(3)
(4)
(5)
(6)
(7)
-0.0115***
-0.0124***
-0.0103***
-0.0109***
-0.0086***
-0.0101***
(0.002)
(0.002)
(0.002)
(0.003)
(0.003)
(0.003)
-0.0239***
-0.0244***
-0.0207***
-0.0233***
-0.0194***
-0.0197***
(0.002)
(0.002)
(0.002)
(0.002)
(0.003)
(0.003)
-0.0003
(0.002)
0.2860***
(0.022)
0.0964***
(0.009)
-0.0049**
(0.002)
-0.0081***
(0.002)
-0.0014
(0.003)
-0.0063**
(0.003)
-0.0108***
-0.0112***
-0.0104***
-0.0093***
-0.0093***
-0.0093***
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
-0.0190***
-0.0195***
-0.0184***
-0.0178***
-0.0177***
-0.0177***
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
-0.0230***
-0.0234***
-0.0221***
-0.0224***
-0.0223***
-0.0223***
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
(0.001)
-0.0218***
-0.0218***
-0.0211***
-0.0220***
-0.0220***
-0.0220***
(0.002)
(0.002)
(0.002)
(0.002)
(0.002)
(0.002)
-0.0246***
-0.0269***
-0.0248***
-0.0241***
-0.0241***
-0.0241***
(0.004)
(0.004)
(0.004)
(0.004)
(0.004)
(0.004)
Yes
Yes
Yes
5,554,369
0.28
Yes
Yes
Yes
5,833,861
0.29
Yes
Yes
Yes
4,837,760
0.29
Yes
Yes
Yes
4,837,760
0.29
Yes
Yes
Yes
4,837,760
0.29
Yes
Yes
Yes
Notes: Robust standard errors in parentheses (clustered at the school level). *** p<0.01, ** p<0.05, * p<0.1. Included controls are: age
dummies, birth order dummies, number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18, month and year dummies.
All specifications include individual fixed effects.
Table A.10: Effect of warnings of neighbors in the bank (standard errors
clustered at zip-code level)
Dependent Variable:
Fraction in Bank Warned
Lag of Frac in Bank Warned
Lead of Frac in Bank Warned
Frac Neighbors Warned
Lag of Frac Neighbors Warned
No of BFP Neighbors
Controls for Own Warning Stage
Controls
Individual FE
Time FE
No. Obs.
R-squared
Noncompliance in Given Month
Benchmark
Placebo
Controls for
Neighbors Warned
(1)
(2)
(3)
-0.0276*** -0.0276***
-0.0349***
(0.008)
(0.009)
(0.006)
-0.0549*** -0.0548***
-0.0284***
(0.011)
(0.011)
(0.004)
0.0004
(0.008)
0.0160
(0.023)
-0.0612**
(0.030)
-0.0000
-0.0000
-0.0000
(0.000)
(0.000)
(0.000)
Yes
Yes
Yes
Yes
4,797,371
0.21
Yes
Yes
Yes
Yes
4,797,371
0.21
Yes
Yes
Yes
Yes
4,797,361
0.21
Notes: Robust standard errors in parentheses (clustered at the zip-code level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: age dummies, birth order dummies,
number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18,
month and year dummies and individual fixed effects.
xii
Table A.11: Effect of warnings of neighbors in the bank
Dependent Variable:
Own Warning Stage
Frac in Bank Warned (WS 1)
Frac in Bank Warned (WS 2)
Frac in Bank Warned (WS 3)
Frac in Bank Warned (WS 4)
Frac in Bank Warned (WS 5)
Controls for Frac
Neighbors Warned (By WS)
Controls
Individual and Time FE
No. Obs.
R-Squared
Noncompliance in Given Month
1
2
3
4
-0.0190***
-0.0160
-0.0083
0.0916
(0.004)
(0.016)
(0.033)
(0.071)
-0.0640*** -0.0430*** -0.0914**
-0.0598
(0.014)
(0.008)
(0.038)
(0.056)
-0.1121***
-0.0414
-0.0472*** -0.1801
(0.023)
(0.040)
(0.014)
(0.121)
-0.0506
-0.2090**
-0.0476
-0.0397*
(0.043)
(0.098)
(0.092)
(0.023)
-0.0218
-0.0301
0.5936
0.5250*
(0.096)
(0.192)
(0.496)
(0.300)
Yes
Yes
Yes
3,842,873
0.27
Yes
Yes
Yes
1,169,159
0.32
Yes
Yes
Yes
420,041
0.34
Yes
Yes
Yes
155,993
0.36
Notes: Robust standard errors in parentheses (clustered at the household level). ***
p<0.01, ** p<0.05, * p<0.1. Included controls are: age dummies, birth order dummies,
number of brothers and sisters in the age categories 6 to 10, 11 to 15, and 16 to 18,
month and year dummies and individual fixed effects.
xiii